The Consequences of Health Care Privatization:
Evidence from Medicare Advantage Exits
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Citation
Duggan, Mark, Jonathan Gruber, and Boris Vabson. “The
Consequences of Health Care Privatization: Evidence from Medicare
Advantage Exits.” American Economic Journal: Economic Policy
10, no. 1 (February 2018): 153–186. © 2018 American Economic
Association
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http://dx.doi.org/10.1257/pol.20160068
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American Economic Association
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Final published version
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http://hdl.handle.net/1721.1/114042
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153
The Consequences of Health Care Privatization:
Evidence from Medicare Advantage Exits
†By Mark Duggan, Jonathan Gruber, and Boris Vabson*
There is considerable controversy over the use of private insurers to deliver public health insurance benefits. We investigate the
con-sequences of patients enrolling in Medicare Advantage (MA),
pri-vately managed care organizations that compete with the traditional fee-for-service Medicare program. We use exogenous shocks to MA enrollment arising from plan exits from New York counties in the early 2000s and utilize unique data that links hospital inpatient utili-zation to Medicare enrollment records. We find that individuals who were forced out of MA plans due to plan exit saw very large increases in hospital utilization. These increases appear to arise through plans both limiting access to nearby hospitals and reducing elective
admis-sions, yet they are not associated with any measurable reduction in
hospital quality or patient mortality. (JEL G22, I11, I12, I13, I18)
T
he Medicare program, which currently provides nearly universal health insur ance coverage to 55 million elderly and disabled US residents, was introduced in 1965 as a form of monopolized insurance coverage that was run and financed by the federal government (Davis, Schoen, and Bandeali 2015). Over time, it has evolved into a hybrid of public insurance and publicly financed private insurance along two channels: the Medicare Advantage (MA) program (Part C) and prescrip tion drug coverage (Part D). The MA program allows Medicare recipients to enroll in a private health insurance plan, which is then reimbursed by the federal govern ment. Prior to 2006, Part C offerings were limited to HMO plans, although additional plan types (such as PPOs) were subsequently introduced, as a result of the Medicare Modernization Act. The Part D program, meanwhile, allows Medicare recipients to choose from a variety of private prescription drug insurance plans (KFF 2014). More than 40 million Medicare recipients are now enrolled in Medicare Part C or Medicare Part D (CMS 2015).* Duggan: Department of Economics, Stanford University, 579 Serra Mall, Stanford, CA 94305 (email:
mgduggan@stanford.edu); Gruber: Department of Economics, Massachusetts Institute of Technology, 77 Massa
chusetts Avenue, Cambridge, MA 02139 (email: gruberj@mit.edu); Vabson: UCBerkeley Haas School of Business,
2220 Piedmont Ave, Berkeley CA, 94720 (email: bvabson@berkeley.edu). We are grateful to Colleen Fiato for
assistance in making the SPARCS data available, to Jonathan Petkun for MCBS analysis, and to Jean Roth for assistance with Medicare enrollment data. We thank Josh Gottlieb, Jacob Wallace, three anonymous referees, and seminar participants at Boston University and NBER for helpful comments. The content is solely the responsibility of the authors and does not necessarily reflect the views of NBER, Stanford, MIT, or the University of California Berkeley. All errors are our own.
† Go to https://doi.org/10.1257/pol.20160068 to visit the article page for additional materials and author
The growing privatization of Medicare has been motivated by potential efficien cies from the “care management” provided by private insurance companies. This is a particularly interesting topic in the context of Medicare Advantage (MA), where private insurers provide coverage side by side with the traditional feeforservice (FFS) system. Evidence on the relative efficiency advantages of private Medicare Advantage plans, however, has been mixed (McGuire, Newhouse, and Sinaiko 2011).
This mixed evidence arises from two key challenges faced by the previous liter ature. The first is the endogeneity of MA enrollment among seniors, for whom this is a choice—individuals have the option to enroll in or disenroll from an MA plan. There is a large body of past evidence which suggests that individuals do not enroll randomly into MA, but rather do so based on health status, leading to potential selection bias when evaluating the impact of MA (Morrissey et al. 2013, Brown et al. 2014). The second is the limited availability of data for those who are enrolled in MA. The Medicare claims’ data that are typically used for empirical work in this area only track utilization for those enrolled in the traditional FFS program, and not those in MA.
The purpose of our paper is to address these empirical concerns with two innova tions. The first is to use hospital discharge data from New York State, which allows us to examine the health care utilization of Medicare recipients both inside and outside of Medicare Advantage. A major advantage of these hospital data is that we obtained permission to longitudinally link it at the individual level to Medicare enrollment files, so that we can assess how an individual’s utilization changes, lead ing up to and following changes in that individual’s MA enrollment status.
The second is to use these novel data to identify the causal impact of MA plan enrollment by studying counties in which MA plans completely exited in the early 2000s and comparing them to counties where there was no exit. In these counties, enrollees who were previously in MA plans had no choice of remaining in MA, so our data allow us to study the utilization impact of moving exogenously from MA plans to the FFS Medicare program.
Doing so, we find that there is a substantial rise in inpatient hospital utilization following MA plan exit. We estimate that those originally in MA see their hospi tal utilization rise by about 60 percent, when moving back to the traditional FFS plan. This estimate is comparable to the corresponding estimate of 65 percent from the RAND Health Insurance Experiment of the 1970s, which randomly assigned patients to managed care plans. The finding is robust to specification checks and appears to be long lasting, suggesting that it does not simply reflect pentup demand that caused a temporary increase in utilization. The increases appear across all types of hospitalizations, but are particularly pronounced for elective visits. We also find substantial reductions in the average distance traveled to the hospital when patients exogenously switch from MA to FFS, following plan exit. This suggests that lower utilization under MA could arise through the mechanisms of reduced hospital avail ability as well as increased restrictions on elective care.
At the same time, we find no evidence that higher FFS utilization is accompanied by higher quality of care, along any dimension. We find no change in the quality of hospitals used by beneficiaries, as measured by typical Medicare metrics. More
significantly, we find no reduction in mortality among those who are forced to move from MA to FFS. Taken together, this suggests that MA plans were delivering care more efficiently than the FFS Medicare program, by using fewer hospital resources. Consequently, our findings have important implications for Medicare, suggesting that increased management of hospital care could lower costs without reducing quality of care.
Our paper proceeds as follows. Section I provides background on the Medicare Advantage program and reviews the previous literature on MA. Section II describes our data. Section III explores the impact of plan exit on utilization and outcomes. Section IV discusses the implications of the findings for Medicare policy. Section V concludes.
I. Background on Medicare Advantage
Since 1982, Medicare recipients have had the option to enroll in privately man aged care plans. Enrollment in the plans has fluctuated in response to changes in the generosity of plan reimbursement and has varied substantially across geographic areas at any point in time (McGuire, Newhouse, and Sinaiko 2011). Throughout the 1980s and 1990s, plan payments for an enrollee were set to be 95 percent of a coun ty’s per capita Medicare FFS expenditures and were further adjusted based on the recipient’s age, gender, disability status, Medicaid enrollment status, and nursing home status (Chaikind and Morgan 2005). The program’s name changed over time, beginning as Medicare managed care and then changing to Medicare+Choice in 1997 and then to Medicare Advantage after 2003. In the pages that follow, we refer to Medicare Part C as Medicare Advantage.
Research demonstrated that individuals enrolling in Medicare managed care plans tended to have significantly lower costs than the average, suggesting that plan contracting actually increased Medicare spending.1 In response to this, legislation
was enacted reducing the future growth rate of private Medicare reimbursement, as part of the 1997 Balanced Budget Act. In this same legislation, the government introduced payment “floors” in counties with low per capita FFS expenditures, given substantially lower private Medicare penetration in those areas. The Benefits Improvement and Protection Act of 2000 further increased payment floors in urban counties that had low per capita FFS expenditures, as described below (Chaikind and Morgan 2005). Despite these changes, the private Medicare enrollment of 5.3 mil lion in 2003 was approximately equal to its 1997 level (5.4 million) (KFF 2014); the increases in enrollment in floor counties were approximately offset by lower enroll ment in other counties. These differential trends in enrollment were driven partly by more modest reimbursement growth across nonfloor counties.
Partly because of stagnating MA enrollment levels, in 2003, the Medicare Modernization Act raised reimbursement across all areas. The government also
1 Studies from the mid1990s found that utilization among private Medicare enrollees was 12 percent (Riley et al.
1996) to 37 percent (PPRC 1996) lower than those of demographically comparable enrollees in FFS. While some of
this could reflect treatment effects rather than selection, the PPRC study actually compared the two groups, during
moved to a system of risk adjustment that began in the early2000s and that paid plans more for individuals with diabetes, pneumonia, or other medical conditions. In 2006, the government moved to a bidding system whereby plans could submit a bid, based on their expected costs of providing traditional Medicare equivalent coverage. If a plan’s bid fell below countylevel benchmarks, the plan would rebate three fourths of the difference to enrollees, in the form of enhanced benefits or reduced premiums, while the government would keep the remainder. If a bid fell above the benchmark, the recipient would pay the full difference between the bid and bench mark, in the form of higher premiums (Chaikind and Morgan 2005). The Affordable Care Act has further transformed plan reimbursement, by gradually reducing bench marks between 2011 and 2017, with the largest reductions occurring in counties with the highest levels of per capita FFS spending (Biles et al. 2012). This increase in reimbursement has led to a steady rise in Medicare Advantage enrollment follow ing 2004, with overall MA enrollment levels increasing by a factor of 3 (17 million) since then, and the share of Medicare beneficiaries in MA increasing by a factor of 2 (31 percent).2
A large body of previous research has investigated the effect of Medicare Advantage on health care expenditures, the utilization of medical care, and health outcomes (see McGuire, Newhouse, and Sinaiko 2011 for an excellent review). One challenge when estimating these effects is the endogeneity of MA enrollment—indi viduals have the option to enroll in or disenroll from an MA plan. To account for this, previous studies have taken a variety of approaches. One subset of research has estimated crosssectional models that include a rich set of controls for individual’s age, health status, and related factors, assuming that there are no remaining unob served differences between those who choose to enroll in managed care and those who do not (Landon et al. 2012). Another set of studies has used instrumental vari able approaches, with their methods assuming that certain factors (e.g., MA pene tration in the local market) influence plan choice but do not affect utilization (Mello, Stearns, and Norton 2002). A final strand of the literature has used longitudinal data to follow individuals over time and compare the evolution of Medicare spending or other outcomes of interest among those switching between MA and traditional Medicare and those not switching; Brown et al. (2014) examine cases of voluntary switching, while Parente et al. (2005) examine cases of switching following plan exit. Critically, plan exit in the latter study is incomplete, meaning that individuals can still remain in MA by switching to a plan that remains active; as such, in both cases, the switching decision between MA and traditional Medicare remains endogenous.
Altogether, the findings from this research are mixed, with most finding that Medicare Advantage does reduce utilization; however, it is difficult to disentangle these estimated effects from favorable selection into MA plans (Mello et al. 2003).
A related literature has examined the effect of MA more generally, in terms of consumer surplus and overall welfare. Town and Liu find that overall marginal costs under FFS are about 40 percent higher than under MA, which is comparable to our own estimate (granted, our estimate applies to inpatient costs only). Meanwhile,
Curto et al. find that FFS costs could be around 14 percent higher than MA, but this estimate is inclusive of administrative costs under MA (which our estimates, of course, are not). Further, Town and Liu assume that there is no advantageous selec tion into MA. Notably, Town and Liu and Curto et al. both identify differences in overall cost rather than differences in utilization; given that unit price levels are likely to be higher under MA than under FFS, by up to 15–20 percent, the cost estimates in these papers would need to be scaled accordingly to reflect the impact on utilization. Altogether, by accounting for selection and isolating the effect on medical utilization from that on overall costs, our paper moves the existing literature forward.
A related area of research has investigated the effect of plan reimbursement on MA enrollment and on the average characteristics of MA enrollees. These stud ies have exploited crosstime variation (Cawley, Chernew, and McLaughlin 2005; Afendulis, Chernew, and Kessler 2013) and crossgeography variation (Cabral, Geruso, and Mahoney 2015; Duggan, Starc, and Vabson 2016) in the generosity of plan reimbursement and find a strong positive effect on MA enrollment.
A third area of research has considered the effect of Medicare Advantage on utili zation for those enrolled in traditional Medicare. The likely mechanism could come through individual health care providers, whose practice style across all patients, inclusive of traditional Medicare, could be a function of the share of their patient load in managed care (Glied and Graff Zivin 2002). This research suggests that reimbursementinduced increases in Medicare Advantage enrollment reduce utili zation among those in traditional Medicare and that this effect partially offsets the greater spending on Medicare Advantage enrollees (Baicker, Chernew, and Robbins 2013; Afendulis, Chernew, and Kessler 2013).
There is a broader literature which has evaluated the impact of managed care on health care utilization. This literature follows the same type of approaches dis cussed above, such as controlling for observable differences across patients in FFS and managed care (Cutler, McClellan, and Newhouse 2000) and instrumenting for managed care enrollment using area factors such as the area penetration of managed care plans (Baker 2000). These studies typically find that managed care plans lower utilization, but are subject to the caveats noted above.
There is, however, one source of exogenous experimental variation, which is an arm of the famous RAND Health Insurance Experiment of the 1970s. Best known for the randomization of individuals across health insurance plans of differential generosity, the RAND HIE also randomized one set of individuals into the Group Health Cooperative of Puget Sound (an HMO) and another set into a feeforservice plan (Manning et al. 1987). This study found very large reductions in inpatient care in the managed care plan, with roughly 65 percent higher inpatient utilization under FFS relative to managed care. At the same time, outpatient utilization was compara ble across the two settings (Manning et al. 1984, Manning et al. 1987).
II. Data and Empirical Strategy
We use administrative datasets from CMS and New York State, which contain information on Medicare and Medicare Advantage enrollment status, individual level utilization metrics for those in MA as well as FFS, and individuallevel
mortality indicators. We have the unique ability to track individuallevel inpatient utilization in Medicare Advantage for every individual in a state and to continuously track individuallevel utilization for those switching between MA and FFS. The dearth of available Medicare Advantage claims’ data has hindered past research and is an issue that we overcome here. In this section, we discuss the various data sources used for this analysis and sample selection restrictions imposed. Further details are provided in the Data Appendix.
A. Medicare and MA Enrollment Data
We obtain administrative Medicare data from CMS, in the form of a denom inator file containing Medicare and Medicare Advantage enrollment status at a personmonth level. This denominator file covers every person enrolled in Medicare, at any point during the 1998–2003 period, and is national in scope. These data also contain information on the demographic characteristics of each enrollee, including birth date and age, gender, race, state of residence, and county of residence. As the Medicare denominator data only identifies overall MA enrollment status, and not the specific plan to which an individual may belong, we supplement the data with publicuse files from CMS, containing national Medicare Advantage enrollment information at a plancountyyear level. Using this publicuse file, we are able to identify the extent to which any US county experienced plan exit, along with the timing of that exit and the characteristics of existing plans. Specifically, we are able to identify those counties experiencing complete plan exit, and the years in which this took place.
B. New York utilization Data
Our primary measures of health care utilization relate to the inpatient setting and cover New York State. These measures are compiled for all those in Medicare, including MA enrollees, by linking specialized New York State dischargelevel hos pital data to Medicare denominator data. This linking is performed using Social Security numbers, which are contained in both of the datasets (the inclusion of these SSN fields in the data required administrative permission from CMS as well as New York State).3 Through this linking, we can construct an individuallevel panel of
inpatient hospital utilization, for the 1998–2003 period across New York State. This panel covers all individuals in Medicare, irrespective of whether they happen to be enrolled in Medicare FFS or Medicare Advantage at any given point, since hospitals compile allinclusive data across all payers. Given our approach for constructing this panel, individuals are included in the sample even if they have had no hospital utilization throughout the study period. With this data, we can bypass issues of sam ple selection that would plague any analysis that uses just standalone hospital dis charge data. Further, given that these data are of uniform coding and completeness
3 Linking was conducted using a combination of the last four digits of individuals’ SSN, dates and years of
birth, gender, and county of residence; in combination, these variables uniquely identify Medicare recipients over 99.9 percent of the time. The Medicare recipients that were not uniquely identified were excluded from the sample.
across payers, any crosspayer differences in utilization would not be driven by differences in underlying data quality; rather, the centralized tracking of these data by hospitals, rather than by individual payers, ensures uniform data quality.
We aggregate our measures of hospital utilization to the personyear level. We focus on cumulative, yearly metrics of the following: number of visits, number of days stayed, number of procedures performed, and the log of hospital charge amounts.4 The means of these utilization measures, for our two cohorts of inter
est, are presented in Table 1. Among those initially in feeforservice Medicare, these measures appear to be at least 60 percent higher than among those initially in
4 To avoid the undue influence of outliers, total charges for those above the ninetyeighth percentile are win
sorized (thus replacing the charge value with the ninetyeighth percentile value).
Table 1—Summary Statistics
Initially MA Initially FFS
Panel A. utilization
Visits 0.177 0.288
(0.782) (1.041)
Total days stayed 1.349 2.333
(8.462) (11.606) Total procedures 0.391 0.635 (2.395) (3.309) Total charges 4,159 5,427 (29,320) (31,654) Panel B. Quality Mortality (percent) 4.193 5.844 (20.045) (23.458) Observations 1,367,730 8,564,475
Panel c. other quality measures
Conditional readmissions 0.202 0.235
(0.402) (0.424)
Conditional preventable visits 0.186 0.178
(0.389) (0.383)
Driving time to hospital 17.83 20.31
(17.83) (24.18)
Driving distance to hospital 6.32 8.36
(10.46) (14.91)
CMS compare hospital rating 0.86 0.85
(0.05) (0.05)
Observations 223,324 2,206,923
Notes: The table presents summary statistics for those in MA and FFS (as
of 1998, respectively). The unit of observation is at the personyear level for
the top two panels and at the hospitalization level for the bottom panel. The sample covers the 1998–2003 period. In addition, the sample is restricted to those over 65, who are also actively enrolled in Medicare. These data were constructed using dischargelevel hospital data from New York State and personmonth level Medicare enrollment records from CMS; these two datasets were linked using SSN and other fields.
Medicare Advantage; however, the extent to which this disparity is driven by patient composition, rather than by treatment differentials, is not readily discernible.
Unfortunately, we are unable to include outpatient data as part of our analyses, as New York State does not collect it centrally. This limits our ability to speak to the impact of Medicare Advantage on total medical spending and overall efficiency. However, past studies on MA suggest that this data limitation may not be problem atic, as these studies suggest that the outpatient effect might be modest or absent. For example, Parente et al. (2005) found that semiinvoluntary MA to FFS switch ing produces no significant effect on outpatient charges, although they do find a 10 percent reduction to physician visits.5 Meanwhile, the one experimental study
of nonMedicare HMOs found no meaningful HMO effect on outpatient utilization, relative to a feeforservice alternative (Manning et al. 1987, Manning et al. 1984).
We have conducted some additional analyses using our own data, to compensate for the lack of outpatient claims, by focusing on visits that are especially suscep tible to offsets. For example, we show limited relative reductions in preventable inpatient visits, specifically ambulatorysensitive visits, which could be especially responsive to increases in outpatient care. We also show that the impacts we find are not particularly concentrated in surgical admissions, for which substitutability to an outpatient setting is most well documented (Avalere Health 2006, MedPAC 2013).
Finally, reductions of inpatient care may be efficiency improving, even if the reductions are offset one for one by increases to outpatient utilization (the same type of care may be more efficient to deliver in the outpatient than inpatient setting). This gives us confidence that there is value in studying inpatient spending, even with a lack of corresponding outpatient data.
C. Mortality Data
We use fields in CMS’s Medicare denominator data to construct personyear mortality indicators. These data are national in scope and cover the entirety of our sample period. In constructing our sample, we allow for sample attrition through mortality; as such, if an individual dies in 2002, their mortality indicator will be pos itive for that year, and the individual will not appear in the sample in the following year. These data are short term in nature—we are only assessing mortality within two years of plan exit—and so they are not comprehensive or perfect measures of care quality. We discuss this point further below.
D. Sample restrictions
We focus on the 1998–2003 period, given that subsequent increases to MA reim bursement resulted in a reentry of plans to many counties that had previously expe rienced exit, with virtually no counties having complete exit of MA plans after this period. We restrict to Medicare recipients over 65 and restrict to those who were
5 However, the study may be inconclusive, as it is potentially biased by selection (individuals typically have
the option of switching to another MA plan in the county, rather than going into FFS, as not all plans in the county
originally eligible for Medicare by virtue of age, rather than disability. We also restrict to those already in Medicare in 1998; as such, we exclude those who aged into Medicare later in the study period. This allows us to construct a baseline mea sure of utilization for every individual in our sample at least two years before any of the MA exits that we study occurred. We construct cohorts based on individuals’ Medicare Advantage/FFS enrollment status at the start of the study period, to com bat bias from voluntary switching between the two at a later point.
Throughout our planexit analyses, our treatment group is made up of eight coun ties that saw complete plan exit, over either a one or two year period. Altogether, these counties accounted for about 3 percent of all Medicare Advantage enrollees in New York State, as of 1998 (which precedes plan exit in every county), and likewise accounted for about 7.5 percent of all FFS recipients. For that year, these eight exit counties had average MA penetration rates of 6.7 percent, compared to an overall New York average of 15.2 percent. In six of the counties, exit is over a oneyear period; in the other two counties, it is over a twoyear period. Meanwhile, our con trol group consists of counties that experienced effectively no plan exit, excluding those counties with partialplan exit over our study period.6
E. Empirical Strategy
As reviewed above, enrollment in an MA plan results from endogenous decisions by seniors that may be correlated with their health status. Thus, any comparison of those who do and do not choose to join MA plans may be biased. Our approach instead is to look at a sample of individuals who exogenously lose access to MA plans: seniors residing in counties where all available MA plans have exited. Such seniors do not have the option of choosing an MA plan. For seniors who were pre viously enrolled in an MA plan, this results in an exogenous shift out of MA into FFS care. As part of our main approach, we do not consider partialplan exits, where some plans leave a county but others remain, due to the endogeneity of the decision to remain in an MA plan; this is done by excluding the two counties experiencing partialplan exit from our sample.
We use the data described above to estimate regressions of the following form: (1) uTi L ict = α + β × Exi t ct + X ict × γ + π c + μ t + ε ict ,
where i indexes individuals, c counties, and t years; uTiL is one of our measures of utilization and/or quality; EXiT is a dummy for whether the MA plans have exited county c in or before year t; X is a limited set of demographic controls (fiveyear age group dummies and gender); and π c and μ t are a full set of county and year fixed effects. For the two counties that exit over two years, the EXiT variable takes on a value of 0.5 in the first year and 1.0 in the second year. In New York, there are 62 counties altogether, of which 8 are exit counties (thereby part of the treated), 52 are counties without substantial exit (thereby part of the control group), and 2 are
counties with partial exit (and are excluded from most analyses). All standard errors are clustered at the county level.
One concern is that disenrollment from MA could result not just from plan exit at a county level, but also from voluntary disenrollments at an individual level, which could require adjustment to our estimates. However, we find the magnitude of such switching to be modest, across treatment as well as control groups. For the treat ment group, we find that about 20 percent of those initially in MA had voluntarily disenrolled from it, over the multiyear period preceding plan exit; this implies that 80 percent of the originally designated treatment group was actually subject to the treatment. We also find that the control group experienced MA disenrollment of similar magnitude during the preperiod, but did not experience meaningful changes in MA enrollment status, right when plan exit was taking place in the other counties. Altogether, this means that all of our coefficient estimates should be divided by 0.8, to reflect the effect of treatment on those actually treated.
F. Endogeneity and Generalizability concerns
A natural concern is that such plan exit is not exogenous with respect to underly ing health care utilization or health status. We address this concern in several ways as part of our empirical work.
First, we include county fixed effects, so that we control for any fixed differences across counties that do or do not experience exits. Second, we investigate whether there are differential trends before the exit “event” itself. Below, we show as well that the pretrends in our key outcomes are very similar between the two groups of coun ties, and that there are no corresponding changes in outcomes for the FFS population. Another approach here would be to find an instrument for plan exit. Unfortunately, no instrument is readily available. One apparent cause of exit was low reimbursement rates. A sizable literature finds that the MA share of Medicare enrollment is strongly related to MA reimbursement rates (Afendulis, Chernew, and Kessler 2013; Cawley, Chernew, and McLaughlin 2005; Pope et al. 2006). In the Appendix, we demonstrate that reimbursement changes over this period are strongly associated with the type of plan exits that we study. In particular, we find that each $100 per month rise in MA reimbursement leads to around a 5 percent decrease in the number of enrollees in exiting MA plans, as a fraction of Medicare recipients in that county. We are unable to use reimbursement changes as instruments for plan exit, however, as they could have direct effects on the treatment of inframarginal MA patients, including those in nonexit counties, and perhaps even spillover effects on the treatment of FFS patients.
Our estimates around plan exit can be validated by examining the effects of an opposite phenomena, plan entry, and showing whether entry is accompanied by uti lization decreases. To perform this exercise, we define our treatment group as those originally in MA, prior to plan exit, in planexit counties. Our control group, mean while, is defined to include those originally in MA, in nonexit counties; this group would have largely remained in MA as of the time of additional plan entry, with its enrollment in MA thereby little affected by the entry. While we find plan reentry to have a highly significant impact on the MA enrollment status of the treatment group, relative to the control group, the impact is modest: following plan exit, most of those
in the treatment group were disenrolled into FFS, whereas following plan reentry, only about 15 percent of the treatment group ended up back in MA. As a result, the confidence intervals for our utilization measures included both zero and our original exit estimates. Altogether, given this lack of power, our results here are ultimately inconclusive.
In addition to endogeneity, another concern is the generalizability of our results. One issue is that exit counties may not be representative of counties more generally, in terms of geography and demographics, composition of beneficiaries, and compo sition of MA plans. Looking first at geography, we show the locations of New York’s exit counties in Figure 1. The map indicates that these counties are found all over the state, although most lie on its eastern border. Turning to demographic and other met rics in Table 2, we find that counties with and without plan exit appear quite similar, along most dimensions. Exit counties have comparable percent urban and percent white to nonexit ones, along with similar MA penetration rates and average incomes. At the same time, exit counties are smaller and less densely populated, on average.
To complement these analyses, we examine the effect of plan exit across the sub urban Long Island counties of Nassau and Suffolk, which are more populated and dense than typical exit counties, but which experienced only partialplan exit and were thereby excluded from our main sample. To this end, these two counties saw exit of a substantial, but not the full, set of their Medicare Advantage plans, resulting in MA disenrollment for about 40 percent of those originally in MA. Examining the impact of plan exit in these counties, we find implied effects that are comparable to our main results for fullplan exit counties. This provides support to the generaliz ability of our findings.
Table 2 also shows a comparison of our New York counties to counties nation wide, to get a sense of national representativeness. Both exit and nonexit counties
New York plan-exit counties New York non-plan-exit counties
in New York are much more urban, more white, have higher incomes, and have higher MA penetration than the nation as a whole. This suggests that while our withinNew York comparisons may be valid, there could be some concern in apply ing these results nationally.
Our results may also not generalize if the MA carriers exiting a county are some how idiosyncratic. For example, if MA exit is due to an insurer going out of busi ness, they may behave differently than general MA insurers (e.g., be less likely to approve nonurgent surgeries). However, far from being idiosyncratic, the set of insurers exiting treatment counties appears to be broad and diverse. In particular, national carriers such as Aetna and WellPoint accounted for over half of all exiting MA plans in New York, at least in terms of preexit enrollment. Given that these carriers are only leaving a limited number of markets, for limited lines of business, rather than departing more broadly, we might not expect the same “goingoutof business” effects that might otherwise materialize.
A final limitation is that our results cover the 1998–2003 period, which might not be completely generalizable to the present day, given the substantial changes that have since taken place in Medicare Advantage (in terms of reimbursement, intro duction of Part D, and introduction of new plan types in addition to HMOs). That said, even with the introduction of new plan types, around twothirds of MA enroll ees continue to be in HMOs, somewhat aiding generalizability. In addition, past research indicates that reimbursement levels may have limited effect on cost sharing and utilization, conditional on an individual’s enrollment in MA (Cabral, Geruso, and Mahoney 2015; Duggan, Starc, and Vabson 2016).
III. Results
As discussed in Part II, here we examine the impact of plan exits on the utiliza tion of health care. Our basic results are illustrated in Figure 2 panels A–C, with the underlying unit of observation here being at a personmonth level.7 Figure 2,
panel A shows the trend in the average annualized number of hospital admissions
7 The level of observation here differs from our regression results, in which observations are aggregated to a
personyear level. To validate these personmonth graphs, we have separately rerun our statistical analyses on data aggregated at a personmonth level. In doing so, we obtain regression results that match what is implied by the graphs.
Table 2—County Profiles
Total Percent Population Percent Average 1998 MA
population urban density white household income pen rate
County type (1) (2) (3) (4) (5) (6)
New York: Exit county 180,808 57% 261 91% 55,974 8.2%
New York: Nonexit county 324,629 55% 3,324 88% 51,156 7.7%
National: All 88,608 41% 268 84% 44,357 4.4%
Notes: The table presents summary statistics for different groups of counties, based on state and planexit status. The unit of observation is at the county level, with the MA enrollment statistics applying for 1998, and all other sta tistics being for 2000. These data were constructed using countylevel characteristics data from the 2000 US census and countyyear level Medicare enrollment records from CMS.
for those who are initially in MA plans in New York counties. The dashed line shows the number of visits for those who are in counties that do not see MA plan exit over this period, while the solid line shows visits for those in counties where MA plans exit. Both are trending up over time because the sample is aging, given that we restrict to individuals who are in Medicare as of 1998. There is a steady upward trend for both sets of counties, but an enormous jump up for counties in which MA plans exit, around the time of that exit. Further, over the postexit period, hospital visits increase more rapidly in exit counties, relative to the pretrend in exit counties as well as relative to the posttrend in nonexit ones. This previews our finding of a robust increase in inpatient utilization among those initially enrolled in MA in exit counties, with part of this increase materializing immediately following plan exit and the remainder emerging gradually over the postexit period.
Panel A. Effect of plan exit: Annualized
inpatient visits Panel B. Effect of plan exit: Annualized length of stay
0.05 0.1 0.15 0.2 0.25 0.3
Annualized inpatient visits
−24 −18 −12 −6 0 6 12 18 24
Months from exit
Annualized length of stay
Months from exit
Panel C. Effect of plan exit: Annualized number of procedures
Annualized number of procedures Months from exit
0.5 1 1.5 2 0.1 0.2 0.3 0.4 0.5 0.6
Initially MA in plan-exit counties (treatment) Initially MA in non-plan exit counties (control)
Initially MA in plan-exit counties (treatment) Initially MA in non-plan exit counties (control)
Initially FFS in plan-exit counties (treatment) Initially FFS in non-plan exit counties (control)
−24 −18 −12 −6 0 6 12 18 24
−24 −18 −12 −6 0 6 12 18 24
Figure 2, panels B–C replicate the format of Figure 2, panel A for the other out come variables that we study: length of stay and number of procedures. In each case, the pattern is similar: roughly flat pretrends with a very large jump at the month of exit, along with additional increases over subsequent months.
The regression analysis of the impact of plan exit is shown in Table 3, for the sample of individuals who are initially in an MA plan. We estimate the change in utilization in counties that see plan exit versus those that do not, while controlling for a full set of county and year indicators. The coefficient of interest corresponds to an interaction term, for being in an exit county and being in the period after exit. Further, the standard errors for all our regression results are clustered at a county level, to control for possible withincounty serial correlation, since that is the level at which plan exit varies. Altogether, the results confirm the implications of Figure 2, panels A–C: there are very sizable increases in utilization along every dimension, with some of the increase happening right at the time of exit and the remainder emerging gradually.
In particular, we show that those MA enrollees who see plan exit in their county (and who therefore move to FFS Medicare) see their number of hospital admissions rise by an average of 0.105; relative to the ex ante mean of 0.177, this represents an increase of approximately 60 percent. Total hospital days rise by 0.65 (48 percent), and the number of hospital procedures rises by 0.13 (33 percent). Total charges rise by 53 percent.8
It is useful to compare our estimates, which (we argue) reflect true differences in the intensity of care across individuals who are exogenously assigned to one
8 We add one to charges given that nearly 90 percent of personyear observations have zero charges and would
otherwise be dropped from the analysis. If we reestimate the model in the level of charges, including zeros (but
allowing perhaps undue influence of outliers), we obtain an estimate that is similar in percentage terms.
Table 3—Effect of Plan Exit on Utilization
Visits Total days stayed Total procedures log total charges
(1) (2) (3) (4)
Mean value 0.177 1.349 0.391 0.939
Exit Cnty 0.105 0.654 0.129 0.533
× PostExit (0.017) (0.146) (0.075) (0.082)
Observations 1,367,730
Sample and controls: Baseline: Initially MA in all New York counties
Notes: The table presents linear regression models, where outcome variables are annualized
measures of individual inpatient utilization. The key variable of interest is Exit Cnty × Post
Exit, which captures the effect of involuntary switching from MA to FFS Medicare. Year, gender, age, and county fixed effects are included as part of the analysis, and standard errors are clustered at the county level. The unit of observation is at the personyear level, for the 1998–2003 period. The sample is restricted to those over 65, who are also actively enrolled in Medicare. In addition, the sample is restricted to those enrolled in Medicare Advantage, as of
the start of the study period (1998). These data were constructed using dischargelevel hospi
tal data from New York state and personmonth level Medicare enrollment records from CMS; these two datasets were linked using SSN and other fields and, subsequently, aggregated to a personyear level. Sample inclusion is not conditional on utilization.
type of plan or another, to the total difference between FFS and MA plans, which also captures patient selection. Focusing on plan exit counties and looking at 1998 (since that year precedes all exits), we find that those initially in MA experience 80 percent fewer yearly hospitalizations relative to the FFS population; by contrast, our main estimated effect (independent of selection) implies 40 percent lower inpa tient utilization under MA than FFS. This suggests that about half of the overall crosssectional difference between FFS and MA utilization in our baseline year is attributable to treatment effects (MA reducing utilization, even holding population fixed) with the remaining half attributable to selection (MA attracting a relatively healthier population). Consistent with this, the MA population appears healthier even in terms of observable characteristics, such as age, given that MA enrollees are on average two years younger than those in FFS.
The results therefore suggest that the exit of MA plans led to very sizable increases in hospital utilization by former MA enrollees, with an estimated magnitude that is comparable to findings from the RAND Health Insurance Experiment (Manning et al. 1987, Manning et al. 1984). The rise in utilization appears to be mostly along the margin of admissions, with proportionally smaller increases in days and in the number of procedures. Given that sicker or more severely injured patients will tend to remain in the hospital for longer, this suggests that the marginal admission is for relatively less serious conditions.
A. Specification checks
We further explore these findings in Table 4, where we consider robustness tests along two dimensions. First, we present a specification that includes both lags and leads of the exit effect. The lead coefficient allows us to test for differential trends across treatment and control counties. The lags allow us to address the important question of whether these large effects simply reflect pentup demand by those who were treated less intensively under MA plans, which would then fade over time as enrollees become acclimated to the FFS environment.
The results of this specification are shown in the first panel of Table 4. We find no significant lead effect, consistent with no differential pretrends across these different types of counties.9 In addition, we find that the estimated utilization response occurs
quickly and gets slightly stronger over the first three years. This is inconsistent with a pentup demand explanation, at least over this three year window. Moreover, it suggests that much of the effect of MA disenrollment is instantaneous and implies that some of the mechanisms underlying MA’s effect are activated immediately and likewise have immediate impact. However, given that the effect size grows over time, mechanisms with nonimmediate effect appear also to be prevalent.
9 In a separate analysis, we find no evidence of increased attrition from exiting plans, in the months immediately
preceding exit. The lack of attrition increases can be attributed to a number of factors. First, information on plan exits only became publicly available 3– 4 months preceding exit; plans typically drop out at the end of each year, while upcomingyear plan availability is only made public in September of the previous year. In addition, there are some individuallevel restrictions on MAtoFFS switching, which typically can only be undertaken during open enrollment periods. Finally, there is substantial inertia in MA enrollment more generally.
Another concern is that, given the relatively small number of exit counties (eight), there may be some other correlated factor that is changing at the same time as plan exit in these same counties. To address this concern, we reestimate our models on the sample of FFS Medicare enrollees in these same New York counties over this same period. These enrollees should be impacted by other factors that impact med ical demand or supply over this period, but should be largely unaffected by the MA exits. Of course, to the extent that there are important spillovers from MA onto the treatment of FFS, then the reduced presence of MA in these counties could lead to increased treatment of FFS beneficiaries. But such an effect would be biased in the same direction as our findings, with those enrolled in FFS initially also using more care when MA plans exit.
Figure 3, panels A–C show the same analysis for FFS enrollees that we showed for MA enrollees in Figure 2, panels A–C. There is a small jump at the time of plan exit, but it is tiny compared to what we see for MA, and it is reflected as well in the nonexit counties. This effect may reflect the spillovers discussed above, but even if reflecting other factors, the effect is very small relative to what we see for the MA population.
This is reflected in regression form in the second panel of Table 4. As expected from the figures, we find no significant or sizable impacts on those enrolled in FFS
Table 4—Utilization Effect: Specification Checks
Visits Total days stayed Total procedures log total charges
(1) (2) (3) (4)
Mean Value 0.177 1.349 0.391 0.939
Exit Cnty × Pre2 −0.004 0.129 −0.014 −0.008
(0.029) (0.211) (0.065) (0.161)
Exit Cnty × Pre1 Baseline
Exit Cnty × First Yr of Exit 0.097 0.711 0.106 0.444
(0.026) (0.184) (0.087) (0.152)
Exit Cnty × Post1 0.113 0.826 0.124 0.529
(0.025) (0.259) (0.077) (0.115)
Exit Cnty × Post2+ 0.100 0.635 0.130 0.579
(0.031) (0.217) (0.109) (0.125)
Observations 1,367,730
Sample and controls: Robustness check: Baseline sample, with leads and lags
Exit Cnty × PostExit −0.005 −0.068 0.121 0.000
(0.009) (0.082) (0.082) (0.048)
Observations 8,564,476
Sample and controls: Placebo test: Initially FFS in all New York counties
Notes: The table presents linear regression models, where outcome variables are annualized measures of individ
ual inpatient utilization. The key variable of interest is Exit Cnty × PostExit. Year, gender, age, and county fixed
effects are included as part of the analysis, while standard errors are clustered at the county level. The unit of obser vation is at the personyear level, for the 1998–2003 period. The sample is restricted to those over 65, who are also
actively enrolled in Medicare. In addition, the sample is restricted to those enrolled in Medicare Advantage (or FFS,
as specified), as of the start of the study period (1998). These data were constructed using dischargelevel hospi
tal data from New York state and personmonth level Medicare enrollment records from CMS; these two datasets were linked using SSN and other fields and, subsequently, aggregated to a personyear level. Sample inclusion is not conditional on utilization.
in our baseline year of 1998 in the counties with plan exit. This suggests that there are not broad trends toward less efficient care in this set of counties (as well as no significant spillovers), and that we are therefore accurately capturing the effect of MA enrollment.
A final concern is that our inpatient data are limited to New York State only and fail to track visits to hospitals in surrounding states. This could result in biased estimates, in the event that MA enrollees in New York have differential rates of outofstate inpatient usage, relative to those in FFS. We perform two different robustness checks, which involve the exclusion of populations more likely to use outofstate hospitals. In one test, we exclude beneficiaries who live in exit coun ties and simultaneously reside within ten miles of a state border. In another test, we take a more systematic approach to identifying potential outofstate hospital users by leveraging hospital service area (HSA) definitions; we exclude those living in exit counties AND simultaneously living in a zip code that is in a non New York HSA. These hospital service area designations reflect actual patterns of hospital use under FFS, as they are based on actual hospital utilization in Medicare FFS, are granular at a zipcode level, and were originally compiled by the Dartmouth Atlas.
Annualized inpatient visits
Months from exit
Panel A. Effect of plan exit on FFS: Annualized inpatient visits
Annualized length of stay
Months from exit
Months from exit
Panel B. Effect of plan exit on FFS: Annualized length of stay
Annualized number of procedures
Panel C. Effect of plan exit on FFS: Annualized number of procedures
Initially FFS in plan-exit counties (treatment) Initially FFS in non-plan exit counties (control) 0.05 0.15 0.2 0.25 0.3 0.1 −24 −18 −12 −6 0 6 12 18 24 0.5 1 1.5 2 −24 −18 −12 −6 0 6 12 18 24 0.7 0.8 0.3 0.4 0.5 0.6 −24 −18 −12 −6 0 6 12 18 24 Figure 3
Ultimately, we find that our original estimates remain unchanged under these robustness tests, suggesting that our estimates are not meaningfully affected by the absence of nonNew York hospital data. For example, when looking at the impact of MA disenrollment on the number of annual hospital visits, we obtain a point esti mate of 0.105 under our main specification, compared to a point estimate of 0.108 when excluding nonNew York HSA areas within exit counties, and a point estimate of 0.105 when excluding parts of exit counties within ten miles of the state border.
B. Mechanisms
The striking increase in medical utilization from MA plan exit raises the ques tion of how MA plans are able to restrain hospital inpatient utilization so effec tively. In this section, we explore the effects on several additional outcome variables, which point to the mechanisms through which managed care plans are restricting utilization.
One possible driver of utilization differences between MA and FFS could be costsharing differentials. Inpatient cost sharing in MA plans typically comes in the form of per day copayments, whereas cost sharing under regular FFS consists primarily of an inpatient (Part A) deductible; daily inpatient copays also appear under traditional FFS, but only for inpatient days in excess of 60, over a single benefit period. Meanwhile, if an individual in FFS opts for supplemental Medicaid insurance, that supplemental insurance will cover some portion of traditional FFS cost sharing. Altogether, the sign of costsharing differentials between MA and FFS is unclear ex ante, given that it is dependent on what individuals do for supplemental Medicare coverage when they lose their MA coverage and on how generous that alternative is relative to Medicare Advantage.
We have investigated this issue using data from the Medicare Current Beneficiary Survey (MCBS), which gathers data for a large nationally representative set of Medicare enrollees on their insurance coverage and medical spending over a two year period. We find that among those leaving Medicare Advantage over the 1998– 2003 period, 29 percent chose not to purchase any supplemental coverage over the next year and therefore face the full extent of Medicare inpatient cost sharing (which is a large deductible for the first 60 days and a daily copayment after that). However, 21 percent obtained supplemental coverage through employersponsored insurance, 36 percent purchased supplemental coverage through the Medigap program, and 13 percent obtained supplemental coverage through government sources (Medicaid or the Military’s Tricare program).
Turning to the generosity of coverage, we find that those in the MCBS with no supplemental coverage bear on average 9.3 percent of their inpatient hospital bills. However, those with some type of supplemental coverage bear about 2.5 per cent of their bills, and this is almost completely invariant to the type of coverage. Regression estimates of inpatient share of costs on dummies for insurance type show no significant difference among all supplemental alternatives, including Medicare Advantage, with or without controls. Therefore, on net, cost sharing among those leaving Medicare Advantage did not change, which means that this cannot explain the reduction in inpatient hospital utilization.
Another mechanism is through restriction of hospital choice, thereby elimi nating the marginal hospitalization (which would be consistent with our results showing more modest percentage effects on charges or days stayed than on num ber of visits). Given that one measure for breadth of hospital choice is distance traveled to hospital (conditional on hospitalization), we examine the impact of MA plan exit on distance traveled and travel time to the hospital, based on the Medicare recipient’s zip code of residence and the zip code of the hospital. As discussed in the Appendix, these distance/time calculations reflect driving rather than “as the crow flies” distances.
Table 5 shows the results for distance traveled. The sample here is restricted to those who actually use the hospital, reducing our sample size. We find that MA plan exit is associated with a sizable reduction in distance traveled to the hospital: the average hospitalization is almost five miles and seven minutes closer in driving
Table 5—Mechanisms for Utilization Impact
Exit Percentage
effect Mean effect Observations
Cohort restriction: Initially MA
County restriction: All New York fullexit or nonexit counties (excludes part exit)
Distance to hospital: Miles −4.780 6.323 −75.6% 223,324
(1.357) (21.5%)
Distance to hospital: Time −6.915 17.825 −38.8% 223,324
(2.334) (13.1%) Emergency hospitalization 0.036 0.132 27.3% 1,367,730 (0.013) (9.8%) Nonemergency hospitalization 0.068 0.045 151.1% 1,367,730 (0.010) (22.2%) Elective hospitalization 0.038 0.029 131.0% 1,367,730 (0.006) (20.7%) Nonelective hospitalization 0.067 0.147 45.6% 1,367,730 (0.017) (11.6%) Elective procedures 0.072 0.076 94.7% 1,367,730 (0.015) (19.7%) Nonelective procedures 0.057 0.315 18.1% 1,367,730 (0.070) (22.2%) Surgery hospitalization 0.017 0.031 54.8% 1,367,730 (0.004) (12.9%) Nonsurgery hospitalization 0.089 0.146 60.9% 1,367,730 (0.014) (9.6%)
Notes: The table presents linear regression models, where outcome variables are various measures of individual
inpatient utilization. The key variable of interest is Exit Cnty × PostExit, which captures the effect of involuntary
switching from MA to FFS Medicare. Year, gender, age, and county fixed effects are included as part of the analy sis, while standard errors are clustered at the county level. The unit of observation is at the hospitalization level for the top panel, and at the personyear level for all the other panels. The data span the 1998–2003 period. The sam ple is restricted to those over 65, who are also actively enrolled in Medicare. In addition, the sample is restricted to
those enrolled in Medicare Advantage, as of the start of the study period (1998). These data were constructed using
dischargelevel hospital data from New York state and personmonth level Medicare enrollment records from CMS; these two datasets were linked using SSN and other fields. For the personyear level sample, inclusion in the sam ple is not conditional on utilization.
time. These represent 76 percent and 39 percent of the sample means, respectively.10
Clearly, enrollees are taking advantage of the less restrictive network under FFS Medicare after MA plan exit. These results are robust to the inclusion of diagnosis related group (DRG) fixed effects, suggesting that they are not driven by composi tional differences in hospital visits across MA and FFS.11
One question raised by these results is the share of the effect attributable to greater travel distance between patients’ place of residence and the hospital. In our analyses, we leverage withinperson variation in distance to the nearest MA hospital in the nonexit counties (to avoid confounding from the direct effects of MA plan exit on hospital utilization). In particular, we estimate a regression of hospital visits on distance to the nearest hospital in the MA network; this regression is restricted to nonexit counties only, with individual fixed effects included to control for fixed locational differences, and the regression being identified only off withincounty network changes over time.12
From this, we estimate the effect of distance to the nearest hospital on utilization, finding that each additional mile from the closest MA network hospital lowers the number of visits by −0.003. We then multiply this estimate by the estimated effect of MA on distance to the nearest hospital, which allows us to derive the effect of MA through this specific channel of distance. Altogether, we find an estimated reduction in hospital admissions of 0.015 from this channel (relative to 0.105 lower admis sions overall), implying that this particular mechanism accounts for about 15 per cent of the overall effect of MA.
Another source of reduced hospitalization under MA plans could be fewer hospi talizations among the least sick enrollees. To assess this, we next explore the change in the types of hospitalizations that take place when MA plans exit. We look at a variety of different types of hospitalizations, and in each case, we can compare the relative effects to the roughly 60 percent overall rise in hospital visits.
We begin, in the second panel of Table 5, by looking at two different types of admissions. The first is “emergency” hospitalizations, which are defined as those requiring immediate medical interventions. We find that the proportional effects for emergency care (at 27 percent) are about half the magnitude of the full sample
10 One concern with this set of estimates is that MA affects the composition of hospitalizations. To the extent
that the marginal admissions are to hospitals that are close to the patient’s home, this would tend to mechanically lower the average distance when patients return to FFS. But given the magnitude of the decline in average distance, this change in composition would not be sufficient to explain the difference even if the average distance for marginal admissions was zero.
11 Recent work on HMOs in the Medicaid setting provides further indication that distance to the nearest hospital
could be a driver of the effect estimated here; in New York’s Medicaid program, the FFS option is not associated
with reduced distance to the nearest hospital and produces only 30 percent higher inpatient utilization (Vabson
2015), compared to the 60 percent increase that we estimate for Medicare. As such, the greater effect of HMOs
under Medicare could be accounted for by a greater effect on distance to the hospital (and other aspects of hospital
networks).
12 One limitation of our approach is that we focus only on distance to the nearest innetwork hospital and not
on broader measures of hospital accessbility. For example, as shown in Ho and Pakes (2014), not all innetwork
hospitals may be equally accessible to managed care enrollees, since capitated PCPs may end up referring only to a subset of innetwork hospitals that are further away and of lower cost. That said, this limitation should be less
applicable to New York than to California, which is the focus of Ho and Pakes (2014), given that capitated PCPs
results (at around 60 percent jump), while, correspondingly, there is a much larger rise in nonemergency hospitalizations relative to the sample mean (151 percent).
In the rows that follow, we divide hospitalizations into those that are elective and nonelective, as specified in the discharge data, which defines elective admissions as those where “the patient’s condition permits adequate time to schedule the admission based on the availability of a suitable accommodation.” We find that there is a much larger proportional rise in elective hospitalizations, which increase by 131 percent of their baseline value after MA plans exit. This is in contrast to nonelective hospi talizations, which rise by less than half (46 percent) of their baseline value.
Indeed, as the next set of rows show, there is a much larger proportional rise in the intensity with which elective hospitalizations are treated. The number of procedures performed rises by 94 percent for elective admissions, and only by 18 percent for nonelective ones.
These results therefore suggest two important mechanisms through which MA plans reduce hospital utilization. The first is to restrict patients to hospitals that involve considerably longer travel. The second is to more tightly restrict elective and nonurgent hospitalizations. These mechanisms are consistent with what has been previously reported on MA plans, in terms of their use of limited provider networks, as well as their implementation of prior authorization requirements and other utili zation management techniques (Blue Cross Blue Shield 2016). These mechanisms are also consistent with the instantaneous timing of the estimated effect, given that the removal of these MA restrictions would immediately follow MA disenrollment and could furthermore have immediate impact.
As noted earlier, one concern given the nature of our data is that we are capturing only increases in inpatient care, and not potential offsetting reductions in outpatient care, when patients move from MA to FFS. While we cannot measure outpatient care, we can consider the type of inpatient care which is most substitutable for out patient care: surgical admissions. Avalere Health (2006) noted the enormous trend around our sample period in shifting surgeries from inpatient to outpatient settings, and MedPAC (2013) further documents that the shift from inpatient to outpatient care was focused on surgeries, with inpatient surgeries declining 3 percent per year from 2005–2011, compared to total inpatient discharges declining only 1 percent per year.
The final rows of Table 5 therefore split the results into surgical and nonsurgical admissions. In fact, we find that the results are, if anything, stronger for nonsurgical admissions, although the results are similar when taken as a share of the respective admission rate. Therefore, there is no evidence of a particularly strong shift in the surgical admissions that are more substitutable for outpatient care.
In Table 6, we examine these mechanisms in further depth, by comparing the effect of plan exit based on individuals’ ex ante distances to innetwork MA hos pitals. MA enrollees living close to innetwork MA hospitals would experience a smaller decrease in hospital distance, following plan exit, compared to MA recipi ents living farther away. We break out our baseline sample of those initially in MA into two cohorts, based on each individual’s distance to their nearest innetwork MA hospital (preplan exit): the closest 50 percent and the furthest 50 percent. We mea sure whether a given hospital is in network based on whether enrollees of MA plans
in the corresponding county visit it at greater than de minimus rates.13 We find that
in these exit counties, 45 percent of hospitals on average (and 47 percent of hospital beds) are classified as in network.
Table 6 shows that the cohort that was closer to an innetwork hospital experi enced a relatively larger increase in utilization, following plan exit. There is both an absolutely and proportionally larger increase in visits, procedures, days stayed, and charges.
The higher level of visits is driven almost entirely by a higher level of admissions from the emergency room. This suggests that restrictions on emergency admissions
13 For these purposes, we define de minimus as receiving fewer than 4 percent of MA hospital admissions, for
a given county. In markets with exiting plans, there typically are only a limited number of hospitals, each of which
would enjoy substantially higher market share, in the absence of network restrictions (we confirm this by looking at
visits under FFS). We do not set these thresholds to zero, given that individuals will go to outofnetwork hospitals
even in the presence of network restrictions.
Table 6—Exit Effect, Based on Distance from InNetwork Hospital Hospital distance Visits Total days stayed Total procedures log total charges Elective visits Emergency visits Variables (1) (2) (3) (4) (5) (6) (7)
Exit Cnty × PostExit −2.972 0.122 0.831 0.178 0.607 0.041 0.052
(0.845) (0.017) (0.142) (0.088) (0.080) (0.005) (0.016)
Mean 5.167 0.186 1.416 0.402 0.988 0.031 0.140
Percent effect −57.5% 65.6% 58.7% 44.3% 61.4% 132.3% 37.1%
(16.4%) (9.1%) (10.0%) (21.9%) (8.1%) (16.1%) (11.4%)
Observations 116,727 682,108 682,108 682,108 682,108 682,108 682,108
Sample and controls: Closest 50% from innetwork MA hospitals
Exit Cnty × PostExit −6.818 0.089 0.477 0.080 0.459 0.036 0.022
(1.817) (0.022) (0.191) (0.066) (0.104) (0.007) (0.013)
Mean 7.577 0.168 1.284 0.382 0.892 0.028 0.124
Percent effect −90.0% 53.0% 37.1% 20.9% 51.5% 128.6% 17.7%
(24.0%) (13.1%) (14.9%) (17.3%) (11.7%) (25.0%) (10.5%)
Observations 106,481 684,166 684,166 684,166 684,166 684,166 684,166
Sample and controls: Furthest 50% from innetwork MA hospitals
Notes: The table presents linear regression models, where outcome variables are various measures of individual
inpatient utilization. The key variable of interest is Exit Cnty × PostExit, which captures the effect of involuntary
switching from MA to FFS Medicare. Year, gender, age, and county fixed effects are included as part of the analysis, while standard errors are clustered at the county level. The unit of observation is at the hospitalization level for the distance measure, and at the personyear level for all other outcome measures. The top panel is restricted to individ uals whose distance to the NEAREST innetwork MA hospital was in the closest 50 percent; note that this refers to distance, preceding the exit of MA plans. The bottom panel, meanwhile, is restricted to individuals in the furthest 50 percent. The data span the 1998–2003 period. The sample is restricted to those over 65, who are also actively enrolled in Medicare. In addition, the sample is restricted to those enrolled in Medicare Advantage, as of the start of
the study period (1998). These data were constructed using dischargelevel hospital data from New York state and
personmonth level Medicare enrollment records from CMS; these two datasets were linked using SSN and other fields. For the personyear level sample, inclusion in the sample is not conditional on utilization.
